Translational fidelity and growth of Arabidopsis require stress-sensitive diphthamide biosynthesis

Diphthamide, a post-translationally modified histidine residue of eukaryotic TRANSLATION ELONGATION FACTOR2 (eEF2), is the human host cell-sensitizing target of diphtheria toxin. Diphthamide biosynthesis depends on the 4Fe-4S-cluster protein Dph1 catalyzing the first committed step, as well as Dph2 to Dph7, in yeast and mammals. Here we show that diphthamide modification of eEF2 is conserved in Arabidopsis thaliana and requires AtDPH1. Ribosomal −1 frameshifting-error rates are increased in Arabidopsis dph1 mutants, similar to yeast and mice. Compared to the wild type, shorter roots and smaller rosettes of dph1 mutants result from fewer formed cells. TARGET OF RAPAMYCIN (TOR) kinase activity is attenuated, and autophagy is activated, in dph1 mutants. Under abiotic stress diphthamide-unmodified eEF2 accumulates in wild-type seedlings, most strongly upon heavy metal excess, which is conserved in human cells. In summary, our results suggest that diphthamide contributes to the functionality of the translational machinery monitored by plants to regulate growth.


REVIEWER COMMENTS
Reviewer #1 (Remarks to the Author): Zhang et al. took a reverse genetics approach to determine whether plants, like fungi and animals, modify eEF2 with diphthamide. They identify an orthologue of the gene that encodes the first committed step of diphthamide biosynthesis, DPH1, and then comprehensively characterize growth and developmental defects in dph1 mutants. Throughout, this report is thorough, experiments are well-executed, and the manuscript is clear and well-written, which made reviewing Zhang et al.'s work a pleasure. Crucially, although diphthamide modification of eEF2 is well-established in humans and yeast, the functional importance of diphthamide modification remains somewhat controversial, and the evolution of this peculiarly "unique" post-translational modification is under scrutiny, as it becomes clear that this pathway has been lost in some lineages of Archaea. Therefore, I think this is a timely and important contribution, and well-suited for publication in Nature Communications, because it will attract a diverse audience of biologists studying the molecular mechanisms of translation, biomedical consequences of diphthamide-related defects, and plant signaling networks. That said, I have a few major concerns about sections where the paper veers off from the focused, comprehensive characterization of dph1 to speculate about downstream impacts of the dph1 on other cellular pathways, especially relating to autophagy and TOR signaling. Briefly, the evidence presented that autophagy is induced and that TOR activity is attenuated is not convincing, and often points to the opposite conclusion. I urge the authors to reevaluate these sections and consider either removing them, openly discussing alternative and conflicting interpretations of their data, or conduct rigorous additional experiments (with an open mind!) to definitively address these hypotheses.
The effect of dph1 on autophagy: (1) I agree that the MDC data presented suggest that autophagy could be induced, but MDC staining is not typically considered sufficient evidence for autophagosome formation (see Klionsky et al., 2008, Autophagy), since this acidotropic dye can label other subcellular compartments.
(2) Autophagy induction is also typically reflected by a transcriptional increase in the expression of autophagy genes, which are otherwise constitutively repressed; in the dph1 transcriptomes, however, none of the hallmarks of autophagy (e.g., ATG8) are induced.
(3) The only other evidence of autophagy presented is an induction of NBR1 total protein levels. Typically, NBR1 mRNA is induced during autophagy or when TOR activity is attenuated (for evidence in Arabidopsis, see Dong et al., 2015, Frontiers in Plant Science, and Scarpin et al., 2020, eLife). NBR1 total protein levels typically decrease upon autophagy induction, however, because NBR1 is also degraded by autophagy. So, most reports that I've seen show lower levels of NBR1 by Western blot, or perhaps aggregation of NBR1-GFP into puncta with ATG8. In other words, the increase in steadystate NBR1 protein levels without a transcriptional induction of NBR1 might actually suggest that autophagic flux is inhibited in dph1. (4) In a related experiment, Extended Data Fig. 6g, in addition to biological replication, these blots should be experimentally replicated (technical replication, I suppose). The lanes clearly didn't run evenly, and I don't know which regions were used for quantification, but I don't really see the strong effect of dph1 on protein ubiquitination reported by the authors. A lack of effect might not be surprising, though, since there's only a slight induction of ribosome frameshifting. I'd also note that misfolded proteins might not be soluble, so this assay might not be the best way to detect the changes the authors hope to report. To address these issues, additional experiments would be required, such as direct demonstration that GFP-ATG8 cleavage is induced in the dph1 background. Ideally, at least two or three lines of evidence (using established standard techniques) should support induction of autophagy, if it is, indeed, induced at all. The yeast data aren't as immediately relevant, to my mind, although I would note as a minor concern that the mutant and wild-type lanes should be compared in a single Western blot (it looks like the mutants were run separately from WT), and this experiment would need to be replicated (or at least, the replication better described).
The effect of dph1 on TOR activity: (1) The blots showing S6K-pT449 and total S6K levels need to be shown, ideally not just one, but all of the replicated experiments conducted in the lab. Quantifying changes in S6K-pT449/S6K is notoriously challenging in Arabidopsis, and results of these Westerns can be overinterpreted. Without seeing these, I can't readily evaluate these results.
(2) The "hypersensitivity" of dph1 to AZD-8055 needs to be quantified and more thoroughly investigated, if this point is worth raising at all. Simplistically, if dph1 already has a defect in cell proliferation, and AZD-8055 broadly inhibits growth (cell expansion and proliferation), it is not surprising that dph1 plants would be much smaller than wild-type upon treatment with AZD-8055 (an "additive" effect). It also isn't immediately clear to me that hypersensitivity to AZD-8055 would indicate already-attenuated TOR activity; alternatively, you might expect that if TOR activity is already attenuated in dph1, AZD-8055 might be less disruptive/impactful than for wild-type plants. To put it another way: if mutants and wild-type plants grow similarly under mock conditions, but the mutant grew much smaller after supplying low concentrations of AZD-8055 that don't affect wild-type growth, you could easily argue that the mutant is hypersensitive to AZD-8055. To thoroughly conduct this experiment, growth assays would need to be repeated using a range of AZD-8055 concentrations, a sort of "kinetic" experiment to identify some concentration or condition where AZD-8055 clearly has a qualitatively and quantitatively stronger impact on dph1 than it does on wild-type plants.
(3) The RNA-Seq experiment doesn't really support repression of TOR activity as a major defect in dph1. For example, when TOR is attenuated, under diverse conditions, the same results are observed: autophagy-related genes are transcriptionally induced and ribosomal protein genes are repressed. Instead, the dph1 transcriptomes show, if anything, an induction of r-protein genes and repression (or no effect) on autophagy-related genes. (4) In plants, it is clear that TOR promotes both cell proliferation and expansion, and has strong effects on developmental timing (e.g., flowering time). As shown here, however, dph1 only impacts proliferation, with little to no impact on expansion. If there were other clear evidence that TOR activity is disrupted, I wouldn't be bothered by this, but given that the other lines of evidence are tenuous (or contradictory), this phenotypic disagreement might be worth reconsidering, too. (5) TCTP1 (a.k.a. TPT1 in humans) levels are also mentioned as a potential proxy for TOR activity. Indeed, TCTP1 protein levels are sensitive to TOR inhibition across eukaryotes, but probably due to translational regulation, not transcriptional regulation (TCTP1 mRNAs begin with a canonical 5'TOP motif regulated by TOR-LARP1 signaling, see Philippe et al., 2020, PNAS and Scarpin et al., 2020, eLife). I couldn't immediately find an instance in the Arabidopsis literature where TCTP1 transcript levels are sensitive to TOR activity. Moreover, the evidence that TCTP1 acts as a GEF is hotly contested (see Rehmann et al., 2008, FEBS Letters for one example, but there are many) and hasn't been supported outside Drosophila (or, for that matter, even in Drosophila), so I think the discussion of TCTP1 potentially acting upstream of TOR signaling should be removed.
In summary, based on the evidence presented, I'm not yet convinced that TOR activity is disrupted in dph1 mutants, and certainly there is no clear demonstration that TOR signaling mediates any of the defects caused by dph1, since many of the canonical functions of TOR are not disrupted in these mutants. I recommend that the authors critically reevaluate their results, consider alternative hypotheses, and, if the hypothesis that dph1 impacts TOR activity is actually important for this study, they should conduct additional experiments (with an open mind) to fully test this hypothesis.
Lastly, throughout the manuscript, it wasn't always immediately clear to me how many times an experiment was replicated-for example, in Fig. 2b, are the blots shown representative of several replicates, or was the experiment only conducted once? There are several places throughout the manuscript where I would just want to know that the experiment was repeated.
Reviewer #2 (Remarks to the Author): These research groups lead the functional analysis of the genes of diphthamide modification in yeast and mammalian cells. Zhang et al. extended their study for the physiological roles of eEF2 diphthamide modification in vascular plant, Arabidopsis. By generating loss-of-function AtDPH1 mutants by T-DNA insertion, they confirmed the defect in eEF2 diphthamide modification in dph1 mutant, using MS analysis and the specific antibody which detects diphthamide-unmodified eEF2. They examined the translation fidelity by using mesophyll protoplasts from dph1 mutant with a reporter for programmed -1 frameshifting. As expected, dph1 mutant showed an increased error rate of programmed -1 frameshifting. Homozygous mutant is viable but biomass and primary root length of seedling were about half of wild type. The developmental timing of leaf formation and flowering was unchanged. Leaf palisade cell size was not affected by dph1 mutation but cell number and endopolyploidy decreased. They also found that the ratio of phospho-S6K/total S6K was decreased in dph1 mutant, suggesting the attenuation of TOR activity. Consistent with this observation, TCTP1, a TOR signaling related protein, was nearly halved in dph1 mutant. Transcriptome analysis indicated the upregulation of abiotic stress response in dph1 mutant. Interestingly, they found that heavy metal toxicity by Cu and Cd was correlated with the accumulation of diphthamide-unmodified eEF2.

Specific comments:
In the absence of dph1, dph5 binding to eEF2 could be enhanced, and dph5 may inhibit eEF2 function. Their previous study indicated that the growth phenotype of dph2 mutant yeast under thermal or chemical stress is sensitive to eEF2 down-regulation. I am wondering if dph1 phenotype could be rescued by eEF2 overexpression.
In mice, defects in genes responsible for diphthamide synthesis can cause embryonic lethality with an abnormality in cranial neural crest, neurodevelopment, and digit formation. Growth defects are also reported in mouse embryos. In the reported MS analysis, they found growth defects and attenuation of TOR signaling in dph1 mutant. The decrease in translation in dph1 mutant could be placed as an upstream of TOR, however, they need to show that the translation is indeed attenuated in seedlings.
They showed dph1 mutant seedlings reduced cell proliferation but not cell size. Which steps of cell proliferation are affected in dph1 mutant? Cell cycle analysis can be performed.
They showed the activation of autophagy in dph1 mutant. Programmed -1 frameshifting may cause an increase of misfolded proteins. They can evaluate the accumulation of such proteins in dph1 mutant seedlings.
The reduction of diphthamide-modified eEF2 by Cu or Cd is interesting. Does Cu or Cd reduce ACP intermediate formation in cells (yeast, MCF-7, or mesophyll protoplasts)?
Reviewer #3 (Remarks to the Author): The article by Zhang et al. provides multiple pieces of evidence of the role of diphthamide modification on eEF2. The experiments are well performed and the article is well structured and easy to read. This article provides the following evidence: 1. The DPH1 protein (involved in the first committing step of diphthamide synthesis) is conserved in Arabidopsis. The Arabidopsis protein presents a conserved His (H700), which is the one modified by the addition of diphthamide in yeast (H699) and in humans (H715). This gene is ubiquitously expressed in Arabidopsis tissues and the protein is localized, as expected, in the cytoplasm. 2. They identified two dph1 mutants that accumulates unmodified (diphthamide) eEF2. These mutants are hypersensitive to hygromycin compared to the wild type and these mutants show elevated -1 frameshifting error rates.
3. The dph1 mutants show reduced biomass and reduced primary root length at the seedling stage, reduced area (with no differences in palisade cell size but a reduced number of cells and endoploidy levels) in leaves, and a reduced meristematic zone in the roots (with lower number of cells and an increase in cell length). 4. The dph1 mutants are hypersensitive to a treatment with a TOR inhibitor and show a reduced TOR activity (based on the decrease in S6K phosphorylation). Consistent with the negative role of TOR in autophagy, these mutants display an enhanced number of autophagosomes and a higher accumulation of the cargo protein NBR1. 5. dph1 mutants show changes at the transcriptional level in genes related to the response to stress. Specifically, dph1 mutants show an upregulation of genes involved in abiotic stress. 6. Treatments with heavy metals reduced the amount of modified eEF2 and correlates with decreased growth and decreased biomass. These results are interesting and provide multiple evidence on the possible role of diphthamide modification on eEF2 in plants. In general terms, the experiments are well performed and support the conclusions. My main concern is that this study does not deepen in the biological aspect of the findings. This deeper analysis is required to provide additional information on current knowledge of diphthamide and DPH1 already known in other eukaryotes. In this sense, some experiments are similar and provide also similar results to the ones described in yeast and mammals (this is the case of the role of diphthamide modification in translation frameshift fidelity, the hypersensitive phenotype of mutants involved in eEF2 modification and of eEF2 mutants to hygromycin and to other translational inhibitors in yeast (Ortiz et al., 2006), the hypersensitive phenotype to TOR inhibitors and the reduced number of cells in culture of mutants with loss of diphthamide modification which is enhanced in the eEF2 undersupply background (Hawer et al., 2018). Since some effects have been already described in other systems, this study seems to suggest that the role of diphthamide modification on eEF2 in plants seems quite conserved. This is, without any doubts, interesting but, unfortunately, reduces the novelty of the results. In my opinion, to increase novelty required for this type of journal, authors should focus in one of the aspects and delve into it, providing further evidence to what is already known in other eukaryotes. Based on the role of this modification in translation fidelity, it seems crucial to carry out analyses at the level of translation that could allow to identify the direct targets of diphthamide regulation. RNAseq analysis does not provide this information and probably only reflects indirect targets of the regulation. Authors could characterize in detail the role of DPH1 and diphthamide in translation, analyzing whether this modification affects specifically the translation of specific mRNAs. It has to be taken into account that a high number of translational regulators could have a dual role, in the one hand modifying general translation and in the other fine-tuning the specific translation of subsets of mRNAs. To carry out this analysis in depth, they can carry out a Riboseq analysis with wt and dph1 mutants. This analysis would help to identify those genes specifically affected by the -1 frameshift error in the absence of diphthamide, providing more light to the role of diphthamide modification in eukaryotes. Furthermore, this analysis could provide additional details on the role of diphthamide in the control of the cell cycle or in the downregulation of TOR activity in the dph1 mutants. Alternatively, other translational analyses or even proteomic analyses would be of high interest to understand the role of the cited modification, identifying the targets of this modification. They also provide evidence that there are a lower number of cells that show a lower level of endoreplication (at least in leaves); however, we do not know how diphthamide regulates the cell cyle and the endoreplication. This is also an interesting question that without a deeper analysis just describes only the surface of the process. A similar argument could be done for the response to heavy metals. In this case it would be very interesting to know phenotypes of the dph1 mutants in response to the heavy metals and how translatome/proteome is affected (which mRNAs suffer the -1 frameshift during their translation and the effect that this has in the possible generation of a new protein/or in the stability of the proteins) in response to the cited metals. Other comments: Line 151-164. Why the size of the cells in the leaf is not altered in the dph1 mutant (despite the cells have a reduced ploidy levels), while the meristematic cells in the root have an increased size? Why is it unchanged in the mature cortex? Which is the role of diphthamide in cell cycle and endoreplication progression? Figures 6 e,f,g. It is hard to see the differences in the accumulation of HSP17.7, HSP17.6 and ubiquitinilated proteins. In this case, it would be extremely interesting to show the statistics. Line 239. In general terms the expression of the HSPs is a marker of stress and not specifically of protein aggregation. If these genes are specific markers of protein aggregation, please, include the reference. Line 240. An accumulation of ubiquitinilated proteins does not necessarily implies a good clearance of cytosolic protein aggregates. It could be also due to a defect in protein degradation leading to the accumulation of ubiquitinilated proteins that could lead to a higher accumulation of aggregates. If dph1 mutants show a higher level of frameshift it is possible that a large portion of the proteins finishes prematurely. Please, provide an explanation to the heat tolerant phenotype of the dph1 mutants. Lines 249-250. The text establishes that Fig5a and extended Data Fig 7a show immunoblots of the unmodified levels of eEF2, however, none of these panels represent immunoblots. Extended Figure 7 panel a. Despite the differences in root growth being quite clear in Figure 1, the differences in root growth are not so obvious in extended data Figure 7a. Is this due to the medium or the developmental stage? Please clarify it.

Reviewer #4 (Remarks to the Author):
In the manuscript of Zhang et al., the authors perform a functional characterization of diphthamide modification on eEF2 in Arabidopsis. They first establish that a diphthamide modification pathway is also found in plants, as is the case in other eucaryotes. They identify the genes needed for the histamine modification in the Arabidopsis eEF2 protein, characterize the plant phenotype in loss of function (knock-out) and (gain of function) complementation lines for DPH1 and investigate the functionality of the modification on plant performance under abiotic stress.
The findings are novel, in fact it is the first diphtamide manuscript specifically focusing on the function of this modification in plants that I could find (apologies if I missed some!). Given the conserved mechanism behind the modification, I believe that this will interest a broad readership.
In more detail: Upon identifying the genes that are orthologues to the yeast and human enzymes of this linear reaction in several plant species they 2 T-DNA insertion mutants catalyzing the first step of the diphtamide biosynthesis in Arabidopsis thaliana (At), and have generated multiple complemented lines under the native DPH1 promoter. The gene characterization is extensive and well rounded, encompassing phenotypic (including intracellular localization), transcript (including RNASeq) and protein analyses (encompassing western blots and mass spectrometry). After this initial characterization the manuscript expands on a more systemic response, under abiotic stress conditions: heavy metal and heat stress. Plants were assayed under static heavy metal conditions (constitutively grown at the respective metal concentration) and the growth inhibition and the decrease of eEF2 modification was found to correlate to the increase of heavy metal in the medium. Generally, I found the methods well described, proper controls were included in the experiments, and the statistics used is appropriate in my opinion.
I was particularly asked to focus on the protein analyses and with that in mind: The mass spectrometry method was easy to follow and I believe it understandable for repetition by others. I appreciated the combined use of standard western blots (Fig 2b) and MS (Fig 2c) as independent confirmations of the post-translational modification (PTM). The MS detection of the diphtamide modification occurs by detection of a m/z difference after MS/MS peptide fragmentation in the Orbitrap Fusion instrument, which is also the case for other PTMs (hopefully making the wider investigation of this PTM easily applicable for other labs that work on protein modifications). The visual presentation of the mass spectra (Fig 2b and Extended Data Fig. 4a) is clear.
In general, this is a novel and well-rounded manuscript that after minor improvement, should be shared with the scientific community. Minor comments are listed below.

REVIEWERS' COMMENTS
Reviewer #1 (Remarks to the Author): Overall, I appreciate the efforts made by the authors, and I remain very impressed with the major points of this manuscript. The comprehensive analysis of dph1 mutants, clear demonstration of the conservation of diphthamide modification in plants, and strong evidence that diphthamide modification of eEF2 is affected by Cu and Cd toxicity is all, to my mind, novel, exciting, worthy, and sufficient for publication in Nature Communications. On the other side, to my mind, the authors continue to stretch credulity with several claims that are not well-supported by the evidence they present on a role for DPH1 upstream of TOR in plants, among some other minor points. With the inclusion of the new S6K-pT449 Western blots, I believe that TOR might sometimes be less active in dph1 mutants (although I note that the results are not very reproducible, as clearly demonstrated by the blots in Extended Data Figure 9-contrast panel a with panels b and c. Would an unbiased reader conclude that repressed TOR activity is a consistent, biologically-important output of dph1 that should be employed to explain several dph1 phenotypes?). Nonetheless, as a phenotype, I think it is reasonable to note that TOR activity is likely lower, without any need for invoking a mechanism.
Personally, I wouldn't talk much (if at all) about TOR in this paper, but that's a matter of opinion/perspective and beyond my scope as a reviewer. Short of that, then, I would ask the authors to carefully reconsider various sentences/claims and to soften them wherever possible. (I like the abstract, for instance: just report that TOR is less active and autophagy is relatively induced, without speculation about these being causal or direct downstream effects of dph1 or TCTP1.) I've highlighted a couple examples from the discussion: Sentences like ll. 314-5: "Decreased TOR activity must account at least partly for the reduced growth of dph1 mutants"-why make this strong assertion without evidence? Why not state "Decreased TOR activity *could* account…"? 340-341: "The activation of autophagy in dph1 mutants can be attributed to decreased TOR activity and an accumulation of misfolded or aggregated peptides…"-again, why not *could* or *might* be attributed? 348-350: "In summary, our results are consistent with a model in which reduced TCTP1 levels lead to the attenuation of TOR activity and the growth phenotypes observed in Arabidopsis dph1 mutants." Sure, but the results are also consistent with the model that TOR acts upstream of TCTP1. The results are also consistent with the model that TOR activity is mildly disrupted as a secondary effect of reduced growth and consequent physiological defects. I could go on with more models, but I think this makes the point: if the evidence presented can support completely opposite models, I'm not sure why you choose to present this model over the others, or present any model about this at all. In the end, all that is shown is that TCTP1 levels are lower in dph1, and then various mechanistic ideas are proposed without experimental support.
A few other points: The new autophagy evidence is much more convincing than in the original submission, and I appreciate the efforts the authors made to conduct these experiments. I still wonder about the NBR1 result: in extended data Fig. 10, panel g, we see actin levels remaining constant after TOR inhibition despite massive (maybe even 10-fold) decrease in RbcL levels shown by CBB, and then we see ~2/3 NBR1 levels (in this one blot) after TOR inhibition. So, again, naively one would say that inhibiting TOR and inducing autophagy decreases NBR1 levels, at least relative to actin (if not to RbcL), consistent with past reports that NBR1 is degraded by autophagic flux. Nonetheless, the evidence in the rest of this extended figure is sufficient to convince most readers that autophagy is apparently induced in dph1 mutants, through whatever mechanism.
I remain skeptical about extended data figure 12; the HSP17 blots are not great quality (especially panel a) and the anti-ubiquitin blots don't give a clear conclusion. I tried quantifying panel c, for instance, and did my best to err on the side of more ubiquitinylated proteins in dph1-and I only could get to 1.1-fold differences (not 1.33, which should be visually obvious). After adjusting for loading with the anti-actin control, I couldn't see any quantitative difference at all. As stated last time, I don't think this takes away from the paper. Instead, I think the authors could reasonably present these data, analyze them without prejudice, and present the results (e.g., it looks like maybe there is more ubiquitinylation and more HSP17 expression in dph1, but the effect is slight and the evidence isn't compelling).
So again, to conclude: I greatly appreciate the improvements to the manuscript, and I think that this is a great paper. Although I disagree with some interpretations, I'm ok with disagreement-but the paper should undergo minor revision to best reflect the evidence that is actually presented, rather than making conclusions and then stretching beyond the experiments to find supportive evidence.
Reviewer #2 (Remarks to the Author): In the revised paper, the authors have adequately answered to my concerns. The new cell cycle analysis helps us for understanding the mechanisms of growth inhibition in dph1 mutant. The data from additional experiments where the addition of Cu increases unmodified eEF2 even in MCF2 is interesting as it suggests that there is regulation of dipthamide modification across species.
Reviewer #3 (Remarks to the Author): I acknowledge the effort made by the authors to improve some specific aspects of the article. In this sense, and focusing on my own concerns, I acknowledge that in this new version the authors have provided interesting data related to the role of DPH1 in DNA replication and cell cycle and endoreplication progression. I generally agree with the answers to my questions; nevertheless, I still think that analyzing the translatome (through Ribo-seq analyses) of the dph1 mutants in this article is important. DPH1 is involved in the diphthamide modification of a translation factor and affects probably specific translation. Therefore, RNAseq data (the analysis of transcripction) only provide indirect information. I do not mean that this information is not valuable, but, in my opinion, this information does not uncover the primary targets involved in the dph1 phenotypes. Most probably, Ribo-seq analysis would directly provide a nice view of the process without the need of looking in Arabidopsis for conserved proteins subjected to diphthamide-dependent -1 frameshift in other organisms.